MATCHING IN EPIDEMIOLOGIC STUDIES:
VALIDITY AND EFFICIENCY CONSIDERATIONS
by
Lawrence L. Kupper, John M. Karon,
David G. Kleinbaum, Donald K. Lewis
Department of Biostatistics
University of North Carolina, Chapel Hill, NC
and
Hal Morgenstern
Department of Epidemiology and Public Health
Yale University, New Haven, CT
Institute of Statistics Mimeo Series No. 1239
JULY 1979
MATCHING IN EPIDEMIOLOGIC STUDIES:
VALIDITY AND EFFICIENCY CONSIDERATIONS
by
I
I
Lawrence L. Kupper , John M. Karon ,
l
David G. Kleinbaum , Hal Morgenstern 2 ,
Md
Donald K. Lewis
l
IDepartment of Biostatistics
University of North Carolina, Chapel Hill, NC
2Department of Epidemiology and Public Health
School of Medicine, and Institution for Social and Policy
Yale University, New Haven, CT
KEYWORDS:
St~dies
matching; follow-up and case-control studies; validity;
efficiency.
ABSTRACT
This paper addresses both validity and efficiency issues with
regard to the use of matching and random sampling as alternative
methods of subject selection in follow-up and case-control studies.
Only the simple situation involving dichotomous disease and exposure
variables, and a single dichotomous matching factor, is considered;
cost considerations (e.g., due to the loss of candidate subjects
because of matching constraints) are ignored.
Given this framework, it is demonstrated that the decision
to match or not should be motivated solely by efficiency considerations.
An efficiency criterion based on a comparison of confidence
intervals under matching and random sampling for the effect measure
of interest (i.e., the risk ratio and risk difference in follow-up
studies and the odds ratio in case-control studies) leads to the
following conclusions.
In follow-up studies, matching on a confounder
is expected to lead to a sizeable gain in efficiency over random
sampling, and matching on a non-confounder is not expected to result
in a loss in efficiency.
In case-control studies, matching on a
confounder is expected to lead to a worthwhile gain in efficiency in
most practical situations of interest, although not to the degree
encountered in follow-up studies; and, matching on a non-confounder
is expected to lead at worst to a loss in efficiency only in
situations of little practical importance.
1.
Introduction
In the field of epidemiology, there is probably no more
misunderstood and hence misused technique than that of matching.
This term itself is quite descriptive, since it refers to a method
of subject selection which "matches" individuals in a comparison
group (e.g., unexposed persons in a follow-up study or controls
in a case-control study) with those in an index series (e.g., the
exposed group in a follow-up study or the case group in a casecontrol study).
The goal of such matching is to make the comparison
group similar to the index group with respect to the distributions
of one or more variables which, although not of primary concern,
need to be controlled or adjusted for when describing an exposuredisease relationship of interest.
Such extraneous factors are
often referred to as potential confounding factors) since their
presence, if ignored, may result in a distorted (or confounded)
impression of the true exposure-disease relationship.
Many distinguished authors have discussed in one way or
another the notions of confounding and matching (see, for example,
Fisher and Patil [1974], McKinlay [1977], Miettinen [1970], and
Seigel and Greenhouse [1973] to name just a few).
In spite of these
discussions, there still appears to be confusion concerning exactly
what purpose matching serves with regard to the control of confounding and under what circumstances, if any, is matching
like~y
to be a worthwhile enterprise.
It is the goal of this paper to address these two important
issues in a quantitative way and to make some definitive recommen-
-2-
dations concerning the use of matching in fOllow-up and
case~control
studies as it pertains to issues of validity (lack of bias) and
efficiency (i.e., precision and power).
It will be seen that our
discussions and subsequent conclusions and recommendations will very
much depend on the type of epidemiologic study design being considered.
In this regard, we will focus on the follow-u; and case-control study
designs, the two designs which most commonly involve the use of
matched samples.
In the discussions to follow, we will utilize a probabilisticbased popUlation model (to be described in the next section), and
we will reach conclusions regarding the relative merits of random
and matched samples by an examination of "expected" cell counts based
on the given model.
We will restrict our attention to the special
case involving a dichotomous disease variable (with levels
present and
levels
D for
0 for absent), a dichotomous exposure variable (with
E and
E for present or absent, respectively), and a
single dichotomous extraneous factor
its two levels).
F (with
F
l
and
F
denoting
O
This is the simplest situation that can be con-
sidered and is the one that has been almost exclusively examined by
other investigators.
Even so, its treatment has previously led to
imprecise and Sometimes even incorrect conclusions; we hope to remedy
this situation here.
Extensions of these concepts to the more
general and realistic situation involving several mutually correlated
extraneous factors is currently underway.
-3-
2.
Probabilistic Model
In this section 1 the probabilistic framework is developed
for the population model we will consider.
The parameters to be
utilized in subsequent discussions are best appreciated if introduced
separately for the follow-up and case-control study situations.
2a.
Follow-up study
In a follow-up studY1 subjects. are selected from each of the
two exposure groups.
this setting.
For
The following probabilities are of interest in
i =0
and 1 1
a. =Pr(O IEF.) ,
1
1
81 ,
=Pr (F.1 IE)
1
and
define:
B.1 = Pr (0 IEF 1. )
8 0 , =Pr(F·IE)
1
1
1/J =Pr(E) .
The association between any two variab1es 1 either conqitiona1 on or
averaged over the levels of a third, can be expressed in terms of
the parameters just defined.
For a follow-up study, the parameters used to measure the
exposure~disease
relationship are typically the risk ratio
the risk difference
the factor
(RD).
In particular. for the i-th stratum of
F,
RR.
1
pr(OIEF )
ai
i
= pr(O\EF ) = Bi
i
and
RD.1 =Pr(OIEF.)
- pr(OIEF.)
= a.1 - B.1
1
.
1
The corresponding crude effect measures are
cRR
=
Pr(OIE)
Pr(OIE)
(RR)
=
a 16n +a08l0
13 1601 + 13 0 600
1
and
-4-
and
Relationships among the variables can also be expressed in
terms of odds ratios
(OR).
In this regard, consider the following
two tables based on joint probabilities:
E
E
D
a 181l 1/J
B180l (1-1/J)
IT
(I-a l ) 81l 1/J
(I-B l )8 0l (1-1/J)
E
D
a 08101/J
B0800 (1~1/J)
D
(I-aO) 8l01/J
(1-B O) 800 (l-1/J)
By appropriate utilization of the cell and column marginal
probabilities for these tables, it is possible to express all the
odds ratios of particular interest to us in terms of the
and
8's.
a's, B's,
For example, the exposure-disease odds ratios, conditional
on the levels of factor
F,
are:
and
. aO(I-B O)
ORO =(OR)delfo = Bo(l-a )
O
OR. 4, RR. when a. and B. are small.
_
note that
1
1
1
1
Without going into further detail, some other odds ratios
of future interest in the follow-up study situation are:
-5-
(OR)ef
8U (1-8 01 )
8U 800
= 8 8 = 8 (1-8 )
01
01 10
11
(1~aO)
.
(31 (1-B O)
.
a
l
(OR)dfle = aOO-a ) ,
l
and,
(OR)dfle
2b.
= B (l-B )
O
l
Case-control study
In a case-control study, subjects are selected separately
from the case and control groups.
relevant in this framework.
For
The following probabilities are
i
=0 and 1, define:
£.1
= Pr(E!DF.)
1
0.
Yl i
= Pr(F.1 ID)
YOi
and
</>
1
= Pr(EIDF.)
1
= Pr(F.1 10) ,
= Pr(D).
For a case-control study, the parameter used to quantify the
strength of the exposure-disease relationship is the odds ratio.
Here, the stratum-specific odds ratios
OR I and ORO
defined earlier
take the form
and
the corresponding crude odds ratio is
cOR
= Pr(E ID) Fr(E 1.Ql
Pr(E ID)Pr(E ID)
=
(£l YU +£OY 10) [(1-t\)Y 01 + (1-o0)Y OO ]
(olY 01 +ooY OO ) [(1-e: 1)y U + (l-e:O)Y lO ] •
-6-
Odds ratios which will be useful to us in a case"contro1
study setting are
(OR)efld
and
Also, with some manipulation of conditional probabilities, it can
be shown that the odds. ratios (OR)dfle
and
defined
(OR)dfje
earlier can be equivalently expressed as
and
(1-£1) (1-00)
where
(OR)dfle
=
YllYOO/YlOY01
=
(1-£0)(1-01)
(OR)df'
We have now described the probabilistic structure of our
population.
In our subsequent discussions on matching, we will be
looking at "expected" cell frequencies based on selecting random and
matched samples from this population, and such expected frequencies
will clearly depend on the study design used.
However, before we can examine matching in any detail, we
need to discuss the phenomenon known as oonfounding.
Such discussion
is necessary in order for us to see what connection, if any, matching
has with regard to issues of validity.
We will consider the follow-
up and case-control study design situations separately.
-7-
3.
3a.
Confounding
Follow-up study
One recommended method for establishing the presence or
absence of confounding in a set of data (e.g' l see Miettinen [1974]
and Rothman [1975]) is to compare the crude effect measure with a
"standardized" effect measure; there is said to be confounding or
no confounding in the data depending on whether or not the crude and
standardized measures differ in value.
For follow-up studies, the
standardized measure is a weighted sum of the stratum-specific risk
ratios or risk differences, with the weights typically being chosen
to reflect the distribution of the extraneous factor over the strata
among either the unexposed or the exposed subjects.
In terms of the
risk ratio, the former choice of weights leads to Miettinen's
"externally" standardized risk ratio [1972, 1979]
s'RR
=
B1 80l
(~)+ B0 800 (~)
B1 80l
+
80 800
the latter choice of weights leads to his "internally" standardized
risk ratio (the well-known standardized mortality or morbidity ratio)
B1 8 11
sRR
== SMR
=
(:1]1 B08l0 [;0)
+
B8
8 8
1 11 + 0 10
0
(For notational simplicity, we will avoid putting "hats" on parameters
to denote sample estimates, although we wish to emphasize that
confounding is generally considered to be a property of the sample.)
It is now easy to specify the necessary and sufficient conditions
for which
cRR = s'RR and for which
cRR = sRR.
In particular, the
-8-
=a O or 8 U
l
and, the latter equality holds if and only if either 8 =8
0
1
former equality holds if and only if either
8
11
=801 ,
From Section 2, it is clear that the condition
equivalent to the condition
(OR) df Ie = I,
is equivalent to the condition
811
=801
(OR)dfle
a
and
(OR)dfle
or
a =a
is
O
l
81 = 80
and that the condition
that the condition
(OR)dfle =1,
is equivalent to the condition
=801 ;
(OR) ef
=1.
The fact that
represent conditional measures of
association, as opposed to an unconditional measure like
(OR)ef'
is
a crucial distinction that has often been overlooked in previous
investigations.
It is clear that the conditions for no confounding,as stated
above. depend on the choice of weights used to form the standardized
measure, which is not an entirely desirable feature.
Also, the
use of any sort of standardized measure can be seriously questioned
when the stratum-specific values vary across the strata.
Indeed, the
use of a summary index is to be recommended only when there is
apppoximate uniformity of the effect measure over the strata.
The
analogy to the situation when the presence of interaction precludes
any worthwhile interpretation of main effects in regression analysis
should be apparent.
It is our opinion that severe lack of uniformity
makes any assessment regarding the presence or absence of confounding
somewhat superfluous.
In such circumstances. it is best simply to
list the stratum-specific values of the effect measure, along with
an assessment. if possible and relevant, of a trend in the measure
over "levels" of the strata.
McKinlay [1977] illustrated via numerical examples the problems
-9-
attendant with using summary indices in the presence of interaction
in pair-matched data, but she provides no theoretical treatment of
confounding.
Seigel and Greenhouse [1975], on the other hand, attempt
to develop some purely theoretical results regarding confounding and
pair-matching, but they make some misleading statements (e.g., see
the Appendix).
If we assume that there is uniformity with respect to risk
ratio, then it is easy to see that
and that
Thus, it is clear that the necessary and sufficient conditions for
no confounding are either
Ct.
l
if
= Ct.O'
and vice versa).
8 = 801
11
r\
or
= So
(which implies
In other words, if either
(or, equivalently, if
(OR)dfle =1),
(OR) ef = 1 or
then there is
no confounding; otherwise (i.e., these odds ratios all differ from 1
in value), then, strictly speaking, there is confounding.
With regard to risk difference, it is straightforward to show
that the assumptionRD =RD
leads to exactly the same necessary
O
l
and sufficient conditions for no confounding that we just obtained
for the risk ratio.
In passing, we note that the assumption
Ct.
(Ct.
l - Sl) = (Ct. O - SO)
implies that
Ct.
o
l
~ "'f So
unless
Sl = SO;
and, in
general, an assumption of uniformity of the risk difference implies
non-uniformity with respect to risk ratio, and vice versa.
This
point has been stressed by Miettinen [1974], Mantel, Brown and Byar [1977],
-10and Kupper and Hogan [1978], and bears repeating.
3b.
Case~contro1
study
If we assume uniformity with respect to odds ratio, then the
necessary and sufficient conditions for which
OR =OR =cOR
1
0
are either that
or
° 1 (1-° 0 )
Since
under the
° 0 (1-° 1)
uniformity assumption, it is clear that the above necessary and
sufficient conditions can be expressed in a number of equivalent ways.
Now, from Section 2, we know that the condition
°C1 (1-°
0)
(1-8 )
o
= 1 equivalently means that
(OR)efla = 1
(i.e., that
1
there is no exposure-factor
F
and, similarly, the condition
(OR) ef Id
in the non-diseased group);
is equivalent to
= 1.
£1°0 [Y ll YOO) =1 is equivalent to
Furthermore, the condition ---0£0 1 Y10 YOl
. .
(1-£1)(1-°0) (Y 11 YOO)
the condition (OR)df Ie =1; and, s1m11ar1y,
(1-£0) (1-° ) YlO YO = 1
1
l
is equivalent to (OR)dfle = 1.
If we do not make the assumption
OR =OR ' then, as was
1
O
the case for risk ratio, the specification of necessary and sufficient
conditions for no confounding requires consideration of some sort of
standardized odds ratio.
s'OR and
sOR
Without going into any details, if
denote Miettinen's externally and internally
-11...,.
standardized odds ratios, respectively, then it can be shown that
s'OR=cOR
and that
if and only if either
sOR = cOR
i= 1
(OR) ef I
if and only if either
or
(OR) df Ie = 1
(OR) ef Id = 1 or
(OR) df Ie = 1.
Thus, as with risk ratio, the no confounding conditions vary with
the choice of standardized measure used.
This now completes our discussion on confounding.
A summary
of the conditions for no confounding by study design type and by
choice of standardized effect measure is presented in Table 1.
TABLE 1
Conditions for No Confounding in Follow-Up and Case-Control
Studies by Choice of Standardized Effect Measure Used.
--- .-Study Design
Case-control
Follow-up
Type
Standardized
Effect
Measure
Conditions
For No
Confounding
s'OR
sOR
(OR)dfle =1
(OR) df Ie = 1
(OR)dfl e = 1
(OR)df Ie = 1
or
or
or
or
(OR) ef ,(OR) ef Id = 1
d =1
=
In the absence of interaction for case-control data,
(OR)ef = 1
NOTE:
sRR
s'RR
(OR) ef = 1
and
In conclusion, we reiterate that, practically speaking,
confounding is an issue only when it manifests as an attribute of the
sample, and that a sample of individuals may exhibit confounding with
respect to one or more factors even when there is no "confounding" in
the population.
Such an undesirable occurrence is simply a manifes-
-12-
tat ion of the method by which the individuals to be studies are
selacted from that population; e.g., matching and even the vagaries
of random sampling can introduce confounding into a sample.
One final comment is in order regarding the question of how
to decide on what set of extraneous factors to consider as potential
confounders in a study.
It is our belief that "this set should be
restricted to include only those extraneous factors considered by
tt~
investigator to be risk factors (i.e., disease determinants),
Tnis list should be decided on at the design stage of the study, and
the uecision should be based on previous empirical evidence aud on
theoretical knowledge concerning the disease process under investigation .. Allowing only risk factors to be potential confounders
follows logically from the desired study objective, namely, to
assess the effect of the exposure variable on the disease process
after controlling for the effects of established disease determinants,
Note that a risk factor
F would necessarily be associated
with a non-null value for
In our'forthcoming discussions on matching, we will utilize
the quantification of confounding given in this section.
ThlS~;,
because we will be comparing matching to random sampling as a method
for selecting subjects from our population, and such a comparison
will be based on examining sample properties determined using
expected cell frequencies.
We will again treat follow-up and case-
control studies separately.
Section 4 will discuss matching with
regard to issues of validity, while Section 5 will deal with questions
of efficiency.
-13-
4.
4a.
Matching:
Validity Considerations
Follow-up study
Suppose we select random samples of
unexposed individuals from our population.
Nl
exposed and
NO
Then, we would obtain, on
the average, the following "expected" cell frequencies:
E
E
0
Nl a l 611
N B 601
Ol
0
N (I-a l ) 611
l
N6
l ll
N (l-f3 )6
O
1 01
N6
0 01
E
E
Na 6
l 0 10
0
0 N (l-a )6
l
O 10
N6
l 10
NB6
O 0 00
NO (l-B O) 600
N6
0 00
Because these frequencies are those expected from random sampling, it
should be clear that the properties of these "typical" data would
exactly duplicate those of our hypothetical population,
Our reasons
for including these rather obvious random sampling results are,
firstly, to highlight the contrast with the structure of the corresponding tables based on selecting matched samples, and, secondly, to help
in our discussions on efficiency to be presented in Section 5.
To examine the consequences of choosing a matched sample of
unexposed subjects, suppose we select, as before, a random sample of
N
I
exposed subjects, but now choose the group of
NO
unexposed
individuals in such a way that the distribution of the factor
the same in the sample of
sample of
NI
NO
exposed people.
F is
unexposed persons as it is in the
Under this sampling scheme, we would
obtain the following tables of expected cell counts:
-14-
E
D
Nl a I 811
D
Nl (I-a l ) 811
N8
I 11
E
NOBI 811
E
NO (I- Bl ) 811
N8
0 ll
D
Nl a 08l0
D
N (I-a ) 810
l
O
N8
1 l0
NO (I-BO)E'lO
N8
0 l0
E
E
D
D
E
NOS0 8l0
N (a 8 +0. 8 )
l l 11 0 10
NO (Sl 811 +B 08l0 )
Nl [(1-a l ) 811
NO [(1-B l ) 8u
+ (1-B
+(l-aO) 8lO ]
N
l
o)8lO ]
NO
Strictly speaking, the matching scheme described here is that
of category or frequency matching,
However, the same expected cell
counts would have been obtained by first matching on an individual
basis (i.e., pair matching) and then ignoring the individual matches
within each of the two strata of the factor F (see the Appendix).
Most other authors (e.g.,
~tiettinen
[1970], Seigel and Greenhouse [1973],
and McKinlay [1977]) have chosen to retain the matched pairs in exactly
the setting we have described.
Although we could have easily done the
same, we feel that a matched pairs analysis is inappropriate here because
of the inherent nonuniqueness of the pairs formed within each level of
the extraneous factor; e.g., within each of the two strata of
F,
any
member of the unexposed group can be paired up with any member of the
exposed group without altering the basic within-stratum structure.
Such
"random" pairing is clearly artificial, and leads (within the framework
we are considering) to a smaller
2
X
statistic value (based on
McNemar's test) than the appropriate one involving just two strata.
-15-
An inspection of the previous tables of expected cell frequencies
based on the category matching of unexposed to exposed subjects reveals
the following.
First of all, the "expected" value of the risk ratio
based on the "expected" cell counts for the overall (pooled) table
is equal to
(0. 8
+0.0810)/(81811 +( 8 ),
1 11
0 10
which is exactly
Miettinen's internally standardized risk ratio
sRR.
The conclusion
to be made here is that the act of category matching itself leads to
a valid estimate of the population
performing a stratified analysis.
SMR,
without the necessity of
So, the fact that a matched sample
has been selected can be ignored at the analysis stage without
introducing a bias in the estimation of the
SMR.
Again, we hasten to
reiterate our concern as to the relevance of such a summary index
when the stratum-specific risk ratios vary considerably in value.
In this regard, note that the two sub-tables do provide the correct
stratum-specific risk ratios, namely
0. /8
1
1 and
and, if
0. /8 ;
0 0
there is uniformity (as was assumed by Seigel and Greenhouse), then,
as we noted earlier,
SMR
=0.1/81 =0.0 /8 0 ,
Note that the matching process itself has insured that there
will be no confounding in these data due to the factor
F,
thus
obviating the need for a stratified analysis on validity grounds (but
. not necessar11y with regard to efficiency).
This is because the
unexposed subjects have been selected specifically so that there will
be no exposure-factor
F association in the data; L e., the odds
ratio is 1 for the table
-16-
E
If
Fl Nle
ll
Noell
Fo Nle lO
NoB IO
Nl
N
0
And, as we know from Section 3a, this is a sufficient condition for
no confounding in a follow-up study.
Clearly, this matching process
eliminates any chance to examine the true exposure-factor
association in the population.
In fact, in the population
may be much different from 1 in value and
F
(OR)ef
sRR may not equal
even though there is no evidence of confounding in the sample.
cRR,
For
random sampling, on the other hand, "confounding" in the population
would generally be reflected as confounding in the observed data,
thus necessitating a stratified analysis.
To summarize, regardless of whether or not we category match
in a follow-up study, we can corne up with a valid estimate of the
population standardized risk ratio.
If we match, we are not required
to perform a stratified analysis on validity grounds; if we do not
match, we may have to conduct a stratified analysis to control for
confounding.
Thus, since a valid estimate of effect can be obtained
in either situation, the decision to match or not must necessarily be
based solely on efficiency considerations (e.g., issues regarding
precision in estimation of effect and/or power in hypothesis testing).
We will now move on to a discussion of the validity issue with
regard to category matching in case-control studies.
In this setting
as well, although we can no longer ignore at the analysis stage the
-17-
fact that a matched sample has been selected l we will find that the
decision to match or not must be based solely on efficiency considerations.
4b.
Case-control study
Suppose we select random samples of
from our population.
N
l
cases and
NO
controls
Then 1 we would obtain the following tables·of
"expected" cell frequencies:
E
E
E
E
D
Nl £lY 11
Nl (l-£l)Y11 Nl Yl1
D
Nl€.OY lO
Nl (l-€.O)Y10 Nly lO
D
NOolY Ol
NO(l-ol)Y Ol NOYOI
D
NOoOY OO
NO(l-oO)Y oo NOY
OO
As we know l these expected frequencies based on the random sampling
of cases and controls provide an exact description of relevant population associations.
We will refer again to these tables in Section 5.
To examine the effects of category matching l suppose we select
a random sample of
N cases, and then choose the NO controls in
l
such a way that the distribution of the factor F is the same in
the sample of controls as it is in the sample of cases.
Under this
sampling scheme, we would obtain the following tables of expected
cell counts:
-18-
E
E
E
-E
Nl £1 Yll
Nl (l-£l)Y ll NlY ll
D
Nl £0YIO
Nl (l-£O)Y10
Nly lO
D NOolY ll
NO(l-Ol)Y ll NOY ll
D NOO OYIO
NO(l-OO)Y lO
NOY IO
D
E
E
Nl (£lYll+€OY IO )
Nl[(l-£l)Yll+(l-£O)YlO]
Nl
D NO (OlYll+OOY IO )
NO[(l-Ol)Yll+(l-OO)Y lO ]
NO
D
An examination of these tables indicates that the effect of
category matching in a case-control study is decidedly different from
that in a follow-up study.
In particular, the "crude" odds ratio
obtained from the combined table (i.e., by ignoring the matching) is
this quantity, like
cOR,
is not a valid estimator of the cornmon
stratum-specific odds ratio when there is confounding.
Thus, it is
apparent that one cannot ignore at the analysis stage the fact that
a matched sample has been chosen in a case-control study, and still
be assured (as in follow-up study) that a valid estimate of the
effect measure of interest will be obtained due solely to the matching
process itself.
In fact, it can be shown that category matching in a casecontrol study accomplishes nothing more than random sampling with
regard to the control of confounding, and, in certain circumstances,
could even introduce confounding into the observed data when random
sampling would not.
To see all this, one need only compare the odds
-19-
ratios
(OR)dfle
and
(OR) efleI
for the tables of expected cell
counts based on matching to those based on random sampling.
Thus,
category matching in a case-control study has nothing to recommend
it over random sampling on validity grounds, since, under either
sampling scheme, a stratified analysis would be required to control
for any confounding present in the data.
Clearly, then, any decision
to match in a case-control study must be based solely on efficiency
considerations; such considerations will be pursued in Section 5.
5.
Matching:
Efficiency Considerations
Based on our earlier findings, it is clear that any
recommendations regarding whether or not to match either in a followup study or in a case-control study will necessarily hinge on
considerations of efficiency.
Since a properly analyzed random
sample preserves validity as well as a correctly handled category
matched sample, while also providing a better representation of the
population under study, the extra effort required in choosing a
matched referent group is worthwhile only if there is expected to be
a reasonable gain in statistical efficiency over random sampling.
Such a gain in efficiency will be reflected, for example, in terms of
increased power of a statistical test procedure (like a Mantel-Haenszel
iJ,
or equivalently, in terms of a tighter confidence interval for
the effect measure of interest.
focus on the latter criterion.
Our discussions on efficiency will
Also, although we are aware that issues
of cost (e.g., due to labor, time, and to the loss of candidate subjects
because of matching constraints) often need to be considered when
deciding whether to match or not, we have chosen on grounds of
-20-
simplicity not to deal with such issues in this paper.
However,
our efficiency studies are currently being extended to deal with
such cost considerations.
Before proceeding, however, we wish to point out that previous
work concerning the efficiency of matched samples for the case of
dichotomous factors (e.g., Worcester [1964], Billewicz [1965],
Miettinen [1968, 1969, 1970] and McKinlay [1975]) has not considered
as we will here for both follow-up and case-control studies the
comparison of confidence intervals for important effect measures
(e.g., risk ratios, risk differences, or odds ratios) for matching
versus random sampling (with stratification when needed).
Worcester
[1964], for example, focused on power considerations only and gave
conditions for which the McNemar x2 statistic for pair-matching
would exceed the ordinary crude
2
X
for unmatched data.
Bi11ewicz
[1965] used simulation techniques exclusively to compare variances of
difference effect measures for pair-matched versus unmatched stratified
analyses.
Using Monte Carlo techniques to compare
2
X
values,
McKinlay [1975] contrasted pair-matching to stratification of
independent samples, and found that pair-matching did not always lead
to a more" powerful test.
Miettinen [1968, 1969] considered for follow-up studies only
the power efficiency (for difference effect measures) of pair-matched
analyses versus unmatched and unstratified analyses in the situation
where 'matching is not required for validity"; based on our previous
conclusions, the phrase in quotes is not meaningful.
Moreover,
Miettinen's power calculations in the unmatched case were based on
-21-
the assumption that "subjects in the two independent comparison
series (of equal size) are randomly paired and that the data are
then analyzed as in the matched pairs design".
Miettinen [1970] has
offered intuitive arguments leading to conditions for which random
sampling without stratification is preferable to pair-matching in
case-control studies; but he provides no quantitative justification
and, moreover, does not consider the comparison of category matching
to stratification without matching when the latter is required for
the control of confounding.
Our work on efficiency involves comparing category matching
to random sampling coupled, when required, with stratification,
and considers an appropriate efficiency criterion (one based on the
variance of the estimator of the effect measure of interest).
Speaking generally for the moment, suppose we let
~
denote
the unknown parameter representing either the common risk ratio or the
common odds ratio in the population (assuming uniformity), as the case
may be.
and
If
estimates of
denote the corresponding stratum-specific
then the weighted linear combination
~,
l =WI (ln~l) + Wo(lnPo) ,
with
(wI +wo) = 1,
would be used to estimate
ln~,
100 (l - a) % large sample confidence interval for
~
leading to a
of the form
The reason for working with logs is because, for moderate to large
samples,
ln~l
and
ln~O
will tend to be more closely normally
-22-
and
distributed than
Further justification (based on
extensive simulation work) for the use of this type of transformation
has been provided by Katz, Baptista, Azen, and Pike [1978].
To compare category matching with random sampling in regard to
'"
efficiency, it is meaningful to consider Yare!)
sampling schemes.
Now, if
and
under the two different
2
(\
0 = Var(.ful.lo)' then it
0
(\
can be shown that the choices for
are
222
/ (0 + ( )
0
1
0
0
and
0
222
/ (0 + ( ),
0
1
1
wI
and
o which minimize
W
respectively.
Yare!)
For this particular
weighting scheme, it follows that
(\
(\
(\
1-1 denotes the risk difference, then ! = w11-1 1 + w01-10 '
the expressions for the weights which minimize Var(l) are as given
Similarly, if
except that
l ±Z
1-
a
'"
a.2 = Var(1-1.),
1
;.;r-:a-r~(l"'-)
1
and the 100 (l - a) % confidence interval is
•
2
Now, let
a~ and a~ denote the values of Var(l) under category
matching and random sampling, respectively; our efficiency results will
be based on a theoretical examination of the difference
a comparison of "expected" confidence intervals involving
(a; -a;)
a~ and
and on
a;.
Howevep, befope ppoceeding with oup discussions of the follow-up
and case-contpol situations, we hasten to point out hepe that the
use of such stpatified analysis - based intepvals can be both unnecessapy
and inefficient when thepe is no confounding; in that instance, the
apppopPiate analysis involves the unstPatified (op cPUde) data layout.
-23-
Sa.
Follow-up study
We will first dispense with the "no confounding" situation.
In particular, if either (OR)ef =1 (Le., 811 =8 01 ) or if (OR)dfle =1
(i.e., Sl =SO)' then matching is a futile exercise because the
appropriate unstratified analysis results will be the same for matching
. and random sampling; this follows directly from an inspection of the
tables at the beginning of Section 4a.
To make efficiency comparisons when confounding is
we
pres~nt,
need to return to the stratified analysis framework introduced earlier.
In particular, the large-sample Taylor series approximation to
""-
variance of InRR.,
1
2
(J. ,
1
the
can be written as
/'
• [1 - Pr (0 IEFi) ]
Var(lnRR.
) , 1
N*l.pr(oIEF.)
1
1
[1 - Pr (0 IEF i) ]
(1)
+ --:-----:-=---
No*.Pr(oIEF.)
1
1
N*
and
are the "expected" numbers of exposed and unexposed
li
subjects appearing in the i-th stratum, i = 0, 1. Similarly, the variance
where
of
"'-
RO.
can be expressed as
1
A
Pr(OIEF.) [1- Pr(OIEF.)]
Pr(OIEF.) [1 - Pr(OIEF.)]
1.
1
Var (RO.) = _,..__--1---:;*:------1--,- +
1
N
N~i
li
•
(2)
The "expected" sample sizes involved in expressions (1) anCl. (2)
will vary depending on whether a random or a matched sample is chosen.
In fact,
and
are the only quantities in expressions (1)
and (2) which depend on the sampling scheme; so, any gain in efficiency
due to matching in a follow-up study can be attributed directly to e1e
fact that the category matching process itself has introduced some
stratum~specific
symmetry with regard to subject allocation.
-24-
and
If we let
2
aiM
denote expression (1) with
and
N
replaced by their values under random sampling and category
Oi
matching, respectively, then an inspection of the tables at the start
2
2
of Section 4a leads to the following expressions for
aIR' a OR '
2
2
aIM' and a :
OM
2
(l -
al )
aIR
= (N ell )a
I
l
2
= (N 8 )a
I 10 O
a OR
(NoeOI)SI
(l - B )
aO)
(1 - a l )
(N I 811 )a l
2
=
2
OM
= (N1eI0)a
O
aIM
a
(l -
(1 -Sl)
+
+
o
(Noe oo )So
.+
(1 -B I )
(N 0811 ) Sl
(1 - ao)
(1 - So).
+
(NoeIO)SO
Now, for notational simplicity, define
(l -
a.1
=
p =
Then,
a
O
al
-=
With
where
a.)
1
b1
a.1
811
801
and
b
(OR) df Ie'
N
= I
pI =
O
1
1)=
(I -
S.1
No
(1 - 811 )
(1 -8 01 )
(OR)dfle
22222
aM = aOMalMI (a OM + aIM)
s.)
1
and
and with
..E..=
(OR) ef'
pI
2
aR
defined analogously,
K is a positive constant depending on the
a's, b's, e's
-25-
Expression (3) pertains to the risk ratio.
It should be clear
from (1) and (2) that the corresponding expression for the risk difference
has exactly the form (3) with a.
N
1
l
replaced by bi = -N B. (1 - B.) .
o
1
a! = a. (1 - a.)
1
1
1
and
b.
1
1
To proceed further
of generality) we specify
which
replaced by
with expression (3), suppose (without loss
F
l
and
so that
If
is always the situation in practice, then it can be shown (we
omit the proof) that the behavior of the sign of expression (3) as a
function of
p=e 1l /e Ol
is as depicted in Figure 1.
FIGURE 1
Under these conditions, it can be shown that the region for
which
(a~ - a~)
>0
shrinks as the risk ratio decreases toward 1,
and expands as the risk ratio increases away from 1.
Also, some
numerical results indicate that the magnitudes of the positive values
tend to be substantially smaller than the magnitudes
of
of the negative values.
Thus, based just on the above findings, we would be inclined to
recommend matching over random sampling as a method of subject selection
in foUow""up studies when confounding is present and when
RR
is the
effect measure because:
i)
the region for which matching is better is larger than
the region for which it is worse;
ii)
the closer the risk ratio is to 1, the more likely it is
that matching will be advantageous; and, this is. the very situation in
which the variance of the effect estimator needs to be as small as
possible to detect only a moderately large risk ratio (say, between
-26-
1.5 and 2.5 in value); and,
the negative values of
iii)
are large in magnitude
compared to the positive values, indicating that the possible gain in
precision is large compared to the possible loss.
As far as the risk difference is concerned, the region for
which
a; >O~
has a shape similar to that for the
although it can appear below the diagonal.
RR
(see Figure 1),
Further theoretical results,
however, were much less useful than those for the risk ratio.
Although the above findings concerning the magnitude and sign
of
2
2
(OM -OR)
suggest that matching will often lead to some gain in
efficiency in follow-up studies when there is confounding, they do not
address the practical issue of whether or not the expected gain is
large enough to make any difference in real-life situations.
In order
to find out, we compared numerically the "expected" 95% confidence
intervals based on matching and random sampling for various sets of
values of the parameters.
For example, we first specified a set of
N , NO/N , and RR (or RD). Then, for the
l
l
420 points (6 ,6 ) over the grid generated by 6 and 8
each
U 0l
U
01
ranging from 0.10 to 0.90 in increments of 0.04 with 8 ll I: 8 01 , we
values for
80 , 8/80 ,
recorded the following quantities:
n
OO
=
number of times out of 420 when both confidence intervals included
the null value (1 for RR and 0 for RD);
nOl = number of times out of 420 when only the interval based on
random sampling covered the null value;
n
lO
=
number of times out of 420 when only the interval based on
matching covered the null value; and,
nIl
=
number of times out of 420 when neither interval covered the
null value.
-27-
Thus, for a'given set of parameter values for which
a large value for
n OO
RR >1
(or RD >0),
suggests that neither interval is very
sensitive at detecting a true non-null effect, while a large value for
nIl
suggests that both intervals are sensitive in this regard.
Furthermore, if
n
>n lO ' this is evidence that matching is preferable
Ol
to random sampling, whereas random sampling gets the nod if nlO >n Ol '
We considered the following parameter values:
So =0.005,
O.05~
13/130 = 2, 3;
NO/N l =1, 2, 3;
The choices for
RD
for the
RR and RD
RR =1.5, 2.5, 4.0.
were determined as the values of
a O =SO(RR); thus, the
where
N =100, 250, 506;
l
(a O -SO),
a
values must necessarily be different
l
cases in order for the uniformity assumption to
hold.
Since there are a large number of parameter value combinations
under consideration, we have only presented in Tables 2 and 3
illustrative subsets of the outcomes for
RR and RD,
respectively.
However, based on all our numerical findings, the following general
statements can be made.
For
RR,
we can distinguish the following two extreme cases:
i)
N and NO are small, the a's and S's are small (so
l
that the ratios (1 -a)/a and (1 -8)/13, which appear in the
expression for the variance of the estimator of lnRR,are large),
and the true
tion,
n OO
RR value is not much greater than 1.
is very large)
nIl
In this situa-
is- zero, and
either zero or very small in value.
n Ol and n lO are
This suggests that neither
matching nor random sampling provides a "sensitive enough!! interval.
-28-
ii)
N a~d NO are fairly large, the a's and B's are
l
moderately large (say, BO ~O.OS), and RR is fairly large (say,
RR ~2.S). Then, nIl is very large, n OO is zero, and n Ol and n lO
are either zero or very small in value.
This suggests that either
method of subject selection will provide a "sensitive enough" interval.
For situations between these two extremes, the n OO and nIl
values are typically smaller in value (so that
nOl and/or n lO are
is always greater than n lO (see
necessarily larger), and
n
Ol
Table 2 for a typical set of results).
These findings suggest that
matching is worthwhile in such fairly common circumstances.
For
RD,
a completely analogous pattern emerges, except that
the variance of the estimator of
sizes of the products
a(l -a)
RD
and
increases or decreases with the
B(l -B); e.g., see Table 3.
Also, in each case considered for
RR and RD,
the confidence
interval width based on matching is shorter, on the average, than
t}~c
corresponding width for random sampling.
Given the limitations to generality imposed by the special
framework in which we are working (and ignoring cost considerations),
then, based on all our findings, we reaommendmatching as a method of
subject selection in foUow-up studies.
One can expect a meaningful
gain in efficiency when matching on a confounder, and can anticipate
no loss in efficiency when matching on a nonconfounder.
Sb.
Case-control study
We will address the "no confounding" situation first.
01 =° 0 ,. or equivalently
(OR)efld=l,
If
then, from an inspection of
the tables at the beginning of Section 4b, it follows that the
"expected" unstratified data layouts for matching and for random
-29sampling will be identical.
Hence, matching is unnecessary, since
random sampling provides comparable efficiency.
matching in this situation is clear:
means that matching on
(OR)efld =1
The futility of
the equality
(OR)efld =
F will have absolutely no
effect on the distribution of the exposure variable in the
D and
D groups.
In contrast, if
(OR) ef I'd ~ 1
(OR) df Ie =1
but
(which also
implies "no confounding"), then a stratified analysis is required
for matched data but not for randomly selected data (again, see the
. tables at the beginning of Section 4b).
This is because the un-
stratified data layout based on matching provides the crude effect
measure
cOR
m
(defined in Section 4b), which will not equal the
uniform odds ratio value
(OR, say) unless
01 =00.
The need to
consider these two case-control study "no confounding'! conditions
separately with regard to efficiency is an added complexity which
does not arise in the follow-up study situation.
To compare equitably the efficiency of matching to randOli1
sampling when
(OR) d.f 1e = 1
but
we will contrast (using the
computer-based approach employed in the follow-up study situation) the
"expected" 95% confidence interval based on stratification after
matching to the "expected" 95% confidence interval based on the
unstratified data layout for random sampling.
This latter interval has
the form
[(OR)e -1.960,
(OR)e +1.960],
where
0
2
= {N
l Pr(E ID) [1 - Pr(E ID)]}-l
+{NOPr(EID)[1 -Pr(EID)]}-l ,
(4)
-30-
Pr(EID) =,E1Y U + LOY 10 '
and
Pr(EI"D) =(\Y01 +ooYOO . The former interval
has a more complex structure for a than the latter, and so we will
defer the discussion of our numerical comparison until we have described
the forms of confidence intervals for
OR based on stratificatioa after
matching and after random sampling.
In particular, the
to
a.12 ,
the variance of
Var(ln
,
large~sample
.en6'R.,
1
Taylor-series approximation
can be written as
~.)~
{N*I.rr(EIDF.)[1
1
1
1
_rr(EIDF.)]}-1
1
'
(5)
where
Ni i
N;i
and
are the "expected" numbers of cases and controls
appearing in the i-th stratum,
i =0, 1.
Then, based on (5) and on
the tables at the beginning of Section 4b, the following expressions
can be obtained for the four stratum-specific variances:
2
1
aIR = (N Y11 )E:l (I - E )
l
l
2
a OR =
1
(N l Y10) EO (I - E0 )
+
1
(NoYOl )° 1 (I -01)
+
1
(NoYOO ) 60 (I - 00)
2
I
1
aIM = (N Y )E (I -E ) + (NO Y11) 6 (I - ( )
1
I 11 I
l
1
2
a OM =
I
(NIYIO)cO(l -co)
+
1
(NOYIO ) 00 (l - 00)
-31-
Thus, the !lexpected" 95% confidence intervals for
OR based on
stratification after matching and after random sampling are of the
form (4) with
2
oM
2 2
2
replaced by
°
2
2
= °OMoU/ (oOM + °lM)
and
respectiv~ly.
The confidence interval evaluation in the "no confounding"
compares interval (4) to
but
situation when
that same form of interval with
oM
replacing
the confidence
0;
interval study in the "confounding" situation when both (OR) df Ie 11
01 100
compares (4) using
OM
for
(J
to (4) using
OR
for
an~~
0.
For each comparison, the following combinations of parameter
values were utilized:
NO/N
OR =1.5, 2.5, 4.0;
N =25, SO, 100;
l
I =1,2,3; 00 =0.10,0.30; 01 =1.5°0 ,2°0 ,2.5°0 ,3° 0 ;
(OR) df Ie
=1 for the "no confounding" comparison;
for the "confounding" comparison.
(OR) df Ie = 2, 3, 4, 5
For each combination of parameter
values, 81 pairs of
(Y ll , YOl ) values were utilized with YII varying
between 0.10 and 0.90 in steps of 0.01 and with YOI then varying
subject to the specified constraint on the value of
(OR)dfle.
4 and 5 illustrate typical results of these two comparisons for
particular combinations of parameter values.
In the "no-confounding" situation, random sampling always
gives a shorter confidence interval than matching for all
Tables
-32-
~ombinations of
parameter values considered.
However 1 the difference
in interval length is of no practical importance except in fairly
uncommon situations when
specifically, when
OR
00 and OR are both large in value; more
~2.5
and the exposure is quite common (e.g"
30% and more of the individuals in each one of the four· stratified
D and
0 groups possess the attribute), then matching can sometimes
lead to a meaningful loss in efficiency.
Table 4 provides one example of the following general
pattern observed for sets of parameter values of practical importance:
i)
if the sample sizes are small,
nIl
ii)
iii)
iv)
n OO
is large and
is zero;
if the sample sizes are large,
nIl
is large;
nOl
is always zero;
for intermediate sample sizes ,
is zero and
n lO
may be non-zero ,
but is most likely to be small.
In
summar~matching
on a particular type of non-confounder
can sometimes lead to a loss in efficiency, although such a loss
will only be of practical importance when considering an unusually
common exposure.
Furthermore, since
(OR)df Ie
=1
is the no con-
founding condition under consideration, and this is characteristic
of a non-risk factor , the policy of considering only disease
determinants in a study would help to avoid such over-matching.
-33In the confounding situation, interpretations of the results
,
are also complicated by the fact that they depend on the sizes of
00
and
OR.
First, suppose that
00 =0.10.
Then, we can identify the
following two extreme situations:
i)
If the sample sizes and
quite large and nIl
OR are small, then n
is
OO
is zero, which means that neither sampling
method can be expected to detect an OR
just slightly greater
than 1.
ii)
If the sample sizes and
zero and
OR are large, then n OO is
is quite large, which means that both methods for
choosing controls are sensitive at detecting an
OR appreciably
greater than 1.
In situations intermediate between these two extremes,
may be fairly large but
n
n
Ol
is always zero (e.g., see Table 5).
lO
And, in every case examined for
00 =0.10, .the confidence interval
based on matching was shorter than that based on random sampling.
These findings tend to favor matching over random sampling.
Let us now consider the case when
00= 0.30.
If
OR
is
small (about 1.5 or so), then neither interval detects such a nonnull value even with fairly large samples.
If
OR is moderate
in size (say, about 2.5), then neither interval is good for small
samples, but both are good for intermediate to large samples.
However, in the situation when both
00
and
OR are large, random.
sampling often provides shorter confidence intervals for
OR, the
advantage becoming more pronounced with very high exposure rates
(e.g., on the order of 60 to 70% or more).
-34In summary, we would say that matching in case-control studies
can provide an important gain in efficiency in the presence of
confounding when the exposure is not overly conunon and when
OR is
not extremely large; however, the gain will not be to the degree
expected in follow-up studies.
and
OR
When the exposure is quite common
is large, then random sampling can yield a shorter
confidence interval.
Thus, given the limitations to generality imposed by the
special framework in which we are working (and ignoring cost
considerations), we recommend that matching be employed in casecontrol studies as a method of subject selection for small to
moderate samples, interrmediate values for
OR,
and for small to
moderate exposure rates; this is the set of circumstances most
often considered in a case-control study situation.
Sc.
Summary of efficiency studies
Table 6 provides a summary of the various analysis
comparisons made between matching and random sampling as a function
. of the type of study design and the nature of the confounding.
Table 7 summarizes the various conclusions we have drawn about
efficiency based on these comparisons.
Acknowledgments
Work on this project was partially supported by NIEHS
Research Career Development Award #S-K04-ES00003 and by NIEHS
Training Grant #1-T32-ES070l8.
-35-
APPENDIX
Follow-up study
The 2 x 2 table of "expected" cell frequencies based on the
(artificial) pair matching of
sample of
N unexposed
subjects to a random
N exposed subjects can be shown to have the following
structure;
0
D
D NP
NQ
D
NS
E
NR
N
The maximum likelihood estimator of the population risk ratio
(assuming uniformity of effect) is calculated as the ratio of the
observed marginal frequency for row 1 to that of column 1, and has
In the face of non-uniformity, this estimator can be quite misleading
(see our earlier remarks on the use of such standardized measures
and also the comments and numerical examples of McKinlay [1977]).
In
such a situation, appropriate analysis of the paired data within each
of the two levels of
F
leads to the correct stratum specific values
-36-
Case-control study
The 2 x 2 table of "expected" cell frequencies based on the
(artificial) pair matching of N controls to a random sample of N
cases has the following structure:
E
NW
E
NX
E
NY
NZ
E
o
N
The maximum likelihood estimator of the population odds ratio
(assuming uniformity of effect) is calculated as the ratio of observed
off-diagonal cell counts, and has an "expected" value of
X El (1 - 0l)Y11 + EO(l - 00)Y lO
Y = (1 - E1)61 y 11 + (l - EO)OOY10
= w10R1
where
w.
1
+
wOORO '
= 0.1 (1- E.)Y
l 1. /
1
1
I 0. (1- E.)y
11.
. 0 1
1
for
i
= 0,
1.
Thus, as
1=
in the fOllow-up study situation, this estimator loses meaning when
the stratum-specific odds ratios differ considerably in value.
any case, stratification with respect to the factor
the correct stratum-specific values
OR I
and ORO'
In
F will provide
-37REFERENCES
BILLEWICZ, W.Z. (1965). "The Efficiency of Matched Samples: An
Empirical Investigation, Biometrics, Vol. 21, 623-644.
FISHER, L. and PATIL, K. (1974). "Matching and Unrelatedness",
American Journal of Epidemiology, Vol. 100, 347-349.
KATZ, D., BAPTISTA, J., AZEN, S.P" and PIKE, M.C. (1978). "Obtaining
Confidence Intervals for the Risk Ratio in Cohort Studies",
Biometrics, Vol. 34, 469-474.
KUPPER, L.L. and HOGAN, M.D. (1978). "Interaction in Epidemiologic
Studies", American Journal of Epidemiology, Vol. 108, 477-453.
MANTEL, N., BROWN, C" and BYAR, D,P, (1977), "Tests for Homogeneity
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-38-
TABLE 2
Comparisons of Confidence Intervals for RR Based on Matching and
Random Sampling: Confounding Present, RR::l.5, So =0.05
N
1
NO
Sl
(OR)df!e
100
100
.10
2.11
250
n
OO
n
Ol
n
10
nIl
420
0
0
0
250
420
0
0
0
500
500
151
110
9
150
100
200
420
0
0
0
250
500
420
0
0
0
500
1,000
0
51
0
369
100
. 300
420
0
0
0
250
750
280
87
0
53
500
1,500
.10
2.11
0
19
0
401
100
100
.15
3.35
420
0
0
0
250
250
354
51
6
9
500
500
39
51
21
309
100
200
420
0
0
0
250
500
159
84
21
156
500
1,000
0
10
0
410
100
300
420
0
0
0
250
750
100
59
0
261
500
1,500
0
2
0
418
.15
3.35
-39TABLE 3
Comparisons of Confidence Intervals for RD Based on Matching and
Random Sampling: Confounding Present, RD =0.075, So =0.05
_.--
._.
-
N
1
NO
SO
100
100
.10
250
(OR)dfle
2.11
n
OO
n
Ol
420
0
250
0
500
500
100
n
10
n
ll
11
0
0
0
409
0
0
0
420
200
300
82
0
38
250
500
0
1
0
419
500
1,000
0
0
0
420
100
300
200
95
0
125
250
750
0
0
0
420
500
1,500
.10
2.11
0
0
0
420
100
100
.15
3.35
420
0
0
0
250
250
0
22
0
398
500
500
0
0
0
420
100
200
360
45
0
15
250
500
0
4
0
416
500
1,000
0
0
0
420
100
300
280
76
0
64
250
750
0
1
0
419
500
1,500
0
0
0
420
.15
3.35
-40-
TABLE 4
Comparisons of Confidence Intervals for OR
Random Sampling: No Confounding, OR = 2.5,
Based on Matching and
=0.10, (OR)df Ie =1
O
Ci
~~-=-=
N1
NO
(OR)ef 1([
°1
--c
n OO
n
Ol
n
10
n
ll
-_.. - =----
81
0
0
0
50
81
0
0
0
100
100
0
0
0
81
25
50
81
0
0
0
50
100
4
0
1
76
100
200
0
0
0
81
25
75
81
0
0
0
50
150
0
0
0
81
100
300
.15
1.59
0
0
0
81
25
25
.20
2.25
81
0
0
SO
SO
78
0
0
2
1
100
100
0
0
0
81
25
81
0
0
0
0
SO
SO
100
0
0
81
100
200
0
0
0
81
25
75
81
0
0
0
50
150
0
0
0
81
100
300
0
0
0
81
25
25
SO
.15
.20
1.59
2.25
-41-
TABLE 5
Comparisons of Confidence Intervals for OR Based on Matching and
Random Sampling: Confounding Present, OR = 2 .5, 00 =0.10, (OR)df Ie =3
N
1
NO
t\
(OR) ef Id
n
OO
n
01
n
10
nIl
;=-=--==
=.==:-:=~
81
0
0
0
50
81
0
0
0
100
100
0
0
0
81
25
50
81
0
0
a
50
100
5
37
0
39
100
.200
0
0
0
81
25
81
0
0
0
50
75
150
0
0
81
100
300
.15
1.59
0
0
0
0
81
25
25
.20
2.25
81
0
0
0
50
50
80
1
0
0
100
100
0
0
0
81
25
50
81
0
0
0
50
100
0
18
0
63
100
200
0
0
0
81
25
75
81
0
0
0
50
150
0
0
0
81
100
300
0
0
0
81
25
25
50
.15
.20
1.59
1
2.25
-42-
TABLE 6
Summary of Analysis Comparisons as a Function of the Type
of Study Design and the Nature of Confounding
MATCHING
RANDOM SAMPLING
,J
NO CONFOUNDING
UNSTRATIFIED
UNSTRATIFIED
CONFOUNDING
STRATIFIED*
STRATIFIED
UNSTRATIFIED
UNSTRATIFIED
STRATIFIED
UNSTRATIFIED
STRATIFIED
STRATIFIED
FOLLOW-UP
STUDY
CASE
CONTROL
STUDY
(OR)efld =1
(OR) ef ld" 11,
(OR) df Ie =1
CONFOUNDING
*Al though a stratified analysis is not requi:red on validity
grounds, it is generally more efficient than an unstratified
analysis in this situation.
TABLE 7
Summary of Conclusions about Efficiency Based on Comparisons in Table 6
FOLLOW-UP
STUDY
(OR) ef 1-'
d =1
CASECONTROL
STUDY
I
I"'l
~
I
e
CONFOUNDING
NO CONFOUNDING
No Expected Loss
From Matching
No expected
loss from
matching
Expected Gain
From Matching
(OR) ef Id F1,
OR and exposure
rates are small
to moderate in
value
(OR)dfle =1
No expected
loss from
matching except
when OR and
exposure rates
are large in
value
e
Expected gain
from matching
I
I
OR and exposure
rates are large
in value
Expected gain
from random
sampling
e
-44-
L..-
-
Figure
Behavior of the sign of
2
2
(OM - OR)
1
1
as a function of